How to get a flawed systematic review and meta-analysis withdrawn from publication: a detailed example

Cochrane normally requires authors to agree to withdraw completed reviews that have been published. This withdrawal in the face of resistance from the authors is extraordinary.

There is a lot to be learned from this letter and the accompanying documents in terms of Courtney calmly and methodically laying out a compelling case for withdrawal of a review with important clinical practice and policy implications.

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Robert Courtney’s wonderfully detailed cover letter probably proved decisive in getting the Cochrane review withdrawn, along with the work of another citizen scientist/patient advocate, Tom Kindlon.

Cochrane normally requires authors to agree to withdraw completed reviews that have been published. This withdrawal in the face of resistance from the authors is extraordinary.

There is a lot to be learned from this letter and the accompanying documents in terms of Courtney calmly and methodically laying out a compelling case for withdrawal of a review with important clinical practice and policy implications.

Especially take a look at the exchanges with the author Lillebeth Larun that are included in the letter.

Excerpt from the cover letter below:

It is my opinion that the published Cochrane review unfortunately fails to meet the standards expected by the public of Cochrane in terms of publishing rigorous, unbiased, transparent and independent analysis; So I would very much appreciate it if you could investigate all of the problems I raised in my submitted comments and ensure that corrections are made or, at the very least, that responses are provided which allow readers to understand exactly why Cochrane believe that no corrections are required, with reference to Cochrane guidelines.

On this occasion, in certain respects, I consider the review to lack rigour, to lack clarity, to be misleading, and to be flawed. I also consider the review (including the discussions, some of the analyses, and unplanned changes to the protocol) to indicate bias in favour of the treatments which it investigates.

robert bob courtneyAnother key excerpt summarized Courtney’s four comments on the Cochrane review that had not yet succeeded in getting the review withdrawn:

In summary, my four submissions focus on, but are not restricted to the following issues:

  • The review authors switched their primary outcomes in the review, and used unplanned analyses, which has had the effect of substantially transforming some of the interpretation and reporting of the primary outcomes of the review;

  • The review fails to prominently explain and describe the primary outcome switching and to provide a prominent sensitivity analysis. In my opinion, the review also fails to justify the primary outcome switching;

  • The review fails to clearly report that there were no significant treatment effects at follow-up for any pooled outcomes in any measures of health (except for sleep, a secondary outcome), but instead the review gives the impression that most follow-up outcomes indicated significant improvements, and that the treatments were largely successful at follow-up;

  • The review uses some unpublished and post-hoc data from external studies, despite the review-authors claiming that they have included only formally published data and pre-specified outcome data. Using post-hoc and unpublished data, which contradicts the review’s protocol and stated methodology, may have had a significant effect on the review outcomes, possibly even changing the review outcomes from non-significant to significant;

  • The main discussion sections in the review include incorrect and misleading reports of the review’s own outcomes, giving a.false overall impression of the efficacy of the reviewed therapies;

  • The review includes an inaccurate assessment of bias (according to the Cochrane guidelines for reporting bias) with respect to some of the studies included in the review’s analyses.

These are all serious issues, that I believe we should not be seeing in a Cochrane review.

Digression: My Correspondence with Tom Kindlon regarding this blog post

James Coyne <jcoynester@gmail.com>

Oct 18, 2018, 12:45 PM (3 days ago)

to Tom

I’m going to be doing a couple of blog posts about Bob, one of them about the details of the lost year of his life (2017) which he shared with me in February 2018, shortly before he died. But the other blog post is going to be basically this long email posted with commentary. I am concerned that you get your proper recognition as fully sharing the honors with him for ultimately forcing the withdrawal of the exercise review. Can you give me some suggestion how that might be assured? references? blogs

Do you know the details of Bob ending his life? I know it was a deliberate decision, but was it an accompanied suicide? More people need to know about his involuntary hospitalization and stupid diagnosis of anorexia.

Kind regards

tom Kindlon
Tom Kindlon

Tom Kindlon’s reply to me

Tom Kindlon

Oct 18, 2018, 1:01 PM (3 days ago)

Hi James/Jim,

It is great you’re going to write on this.

I submitted two long comments on the Cochrane review of exercise therapy for CFS, which can be read here:

<https://www.cochranelibrary.com/cdsr/doi/10.1002/14651858.CD003200.pub7/detailed-comment/en?messageId=157054020&gt;

<https://www.cochranelibrary.com/cdsr/doi/10.1002/14651858.CD003200.pub7/detailed-comment/en?messageId=157052118&gt;

Robert Courtney then also wrote comments. When he was not satisfied with the responses, he made a complaint.

All the comments can be read on the review here:

<https://www.cochranelibrary.com/cdsr/doi/10.1002/14651858.CD003200.pub7/read-comments&gt;

but as I recall the comments by people other than Robert and myself were not substantial.

I will ask what information can be given out about Bob’s death.

Thanks again for your work on this,

Tom

The Cover Letter: Did it break the impasse about withdrawing the review?

from:     Bob <brightonbobbob@yahoo.co.uk>

to:            James Coyne <jcoynester@gmail.com>

date:     Feb 18, 2018, 5:06 PM

subject:                Fw: Formal complaint – Cochrane review CD003200Sun, Feb 18, 1:15 PM

THIS IS A COPY OF A FORMAL COMPLAINT SENT TO DR DAVID TOVEY.

Formal Complaint

12th February 2018

From:

Robert Courtney.

UK

To:

Dr David Tovey

Editor in Chief of the Cochrane Library

Cochrane Editorial Unit

020 7183 7503

dtovey@cochrane.org

Complaint with regards to:

Cochrane Database of Systematic Reviews.

Larun L, Brurberg KG, Odgaard-Jensen J, Price JR. Exercise therapy for chronic fatigue syndrome. Cochrane Database Syst Rev. 2017; CD003200. DOI: 10.1002/14651858.CD003200.pub7

Dear Dr David Tovey,

This is a formal complaint with respect to the current version of “Exercise therapy for chronic fatigue syndrome” by L. Larun et al. (Cochrane Database Syst Rev. 2017; CD003200.)

First of all, I would like to apologise for the length of my submissions relating to this complaint. The issues are technical and complex and I hope that I have made them easy to read and understand despite the length of the text.

I have attached four PDF files to this email which outline the details of my complaint. In 2016, I submitted each of these documents as part of the Cochrane comments facility. They have now been published in the updated version of the review. (For your convenience, the details of these submissions are listed at the end of this email with a weblink to an online copy of each document.)

I have found the responses to my comments, by L. Larun, the lead author of the review, to be inadequate, especially considering the seriousness of some of the issues raised.

It is my opinion that the published Cochrane review unfortunately fails to meet the standards expected by the public of Cochrane in terms of publishing rigorous, unbiased, transparent and independent analysis; So I would very much appreciate it if you could investigate all of the problems I raised in my submitted comments and ensure that corrections are made or, at the very least, that responses are provided which allow readers to understand exactly why Cochrane believe that no corrections are required, with reference to Cochrane guidelines.

On this occasion, in certain respects, I consider the review to lack rigour, to lack clarity, to be misleading, and to be flawed. I also consider the review (including the discussions, some of the analyses, and unplanned changes to the protocol) to indicate bias in favour of the treatments which it investigates.

Exercise as a therapy for chronic fatigue syndrome is a highly controversial subject, and so there may be more of a need for independent oversight and scrutiny of this Cochrane review than might usually be the case.

In addition to the technical/methodological issues raised in my four submitted comments, I would also like you to consider whether there may be a potential lack of independence on the part of the authors of this review.

All of the review authors, bar Price, are currently working in collaboration on another Cochrane project with some of the authors of the studies included in this review. (The project involves co-authoring a protocol for a future Cochrane review) [2]. One of the meetings held to develop the protocol for this new review was funded by Peter White’s academic fund [1]. White is the Primary Investigator for the PACE trial (a study included in this Cochrane review).

It is important that Cochrane is seen to uphold high standards of independence, transparency and rigour.

Please refer to my four separate submissions (attached) for the details of my complaint regarding the contents of the review. As way of an introduction, only, I will also briefly discuss, below, some of the points I have raised in my four documents.

In summary, my four submissions focus on, but are not restricted to the following issues:

  • The review authors switched their primary outcomes in the review, and used unplanned analyses, which has had the effect of substantially transforming some of the interpretation and reporting of the primary outcomes of the review;
  • The review fails to prominently explain and describe the primary outcome switching and to provide a prominent sensitivity analysis. In my opinion, the review also fails to justify the primary outcome switching;
  • The review fails to clearly report that there were no significant treatment effects at follow-up for any pooled outcomes in any measures of health (except for sleep, a secondary outcome), but instead the review gives the impression that most follow-up outcomes indicated significant improvements, and that the treatments were largely successful at follow-up;
  • The review uses some unpublished and post-hoc data from external studies, despite the review-authors claiming that they have included only formally published data and pre-specified outcome data. Using post-hoc and unpublished data, which contradicts the review’s protocol and stated methodology, may have had a significant effect on the review outcomes, possibly even changing the review outcomes from non-significant to significant;
  • The main discussion sections in the review include incorrect and misleading reports of the review’s own outcomes, giving a.false overall impression of the efficacy of the reviewed therapies;
  • The review includes an inaccurate assessment of bias (according to the Cochrane guidelines for reporting bias) with respect to some of the studies included in the review’s analyses.

These are all serious issues, that I believe we should not be seeing in a Cochrane review.

These issues have already caused misunderstanding and misreporting of the review in academic discourse and publishing. (See an example of this below.)

All of the issues listed above are explained in full detail in the four PDF files attached to this email. They should be considered to be the basis of this complaint.

For the purposes of this correspondence, I will illustrate some specific issues in more detail.

In the review, the following health indicators were used as outcomes to assess treatment effects: fatigue, physical function, overall health, pain, quality of life, depression, anxiety, and sleep. All of these health indicators, except uniquely for sleep (a secondary outcome) demonstrated a non-significant outcome for pooled treatment effects at follow-up for exercise therapy versus passive control. But a reader would not be aware of this from reading any of the discussion in the review. I undertook a lengthy and detailed analysis of the data in the review before i could comprehend this. I would like these results to be placed in a prominent position in the review, and reported correctly and with clarity, so that a casual reader can quickly understand these important outcomes. These outcomes cannot be understood from reading the discussion, and some outcomes have been reported incorrectly in the discussion. In my opinion, Cochrane is not maintaining its expected standards.

Unfortunately, there is a prominent and important error in the review, which I believe helps to give the mis-impression that the investigated therapies were broadly effective. Physical function and overall-health (both at follow-up) have been mis-reported in the main discussion as being positive outcomes at follow-up, when in fact they were non-significant outcomes. This seems to be an important failing of the review that I would like to be investigated and corrected.

Regarding one of the points listed above, copied here:

“The review fails to clearly report that there were no significant treatment effects at follow-up for any pooled outcomes in any measures of health (except for sleep, a secondary outcome), but instead the review gives the impression that most follow-up outcomes indicated significant improvements, and that the treatments were largely successful at follow-up”

This is one of the most substantial issues that I have highlighted. This issue is related to the primary outcome switching in the review.

(This relates to assessing fatigue at long-term follow-up for exercise therapy vs passive control.)

An ordinary (i.e. casual) reader of the review may easily be left with the impression that the review demonstrates that the investigated treatment has almost universal beneficial health effects. However there were no significant treatment effects for pooled outcome analyses at follow-up for any health outcomes except for sleep (a secondary outcome ). The lack of universal treatment efficacy at follow-up is not at all clear from a casual read of the review, or even from a thorough read. Instead, a careful analysis of the data is necessary to understand the outcomes. I believe that the review is unhelpful in the way it has presented the outcomes, and lacks clarify.

These follow-up outcomes are a very important issue for medical, patient and research communities, but I believe that they have been presented in a misleading and unhelpful way in the discussions of the review. This issue is discussed mainly in my submission no.4 (see my list of PDF documents at the bottom of this correspondence), and also a little in submission no.3.

I will briefly explain some of the specific details, as way of an introduction, but please refer to my attached documents for the full details.

The pre-specified primary outcomes were pooled treatment effects (i.e. using pooled data from all eligible studies) immediately after treatment and at follow-up.

However, for fatigue, this pre-specified primary outcome (i.e. pooled treatment effects for the combination of data from all eligible studies) was abandoned/switched (for what i consider to be questionable reasons) and replaced with a non-pooled analysis. The new unplanned analysis did not pool the data from all eligible studies but analysed data from studies grouped together by the specific measure used to assess fatigue (i.e. grouped by the various different fatigue questionnaire assessments).

Looking at these post-hoc grouped outcomes, for fatigue at follow-up , two out of the three grouped outcomes had significant treatment effects, and the other outcome was a non-significant effect. This post-hoc analysis indicates that the majority of outcomes ( i.e. two out of three) demonstrated a significant treatment effect , however, this does not mean that the pre-specified pooled analysis of all eligible studies would have demonstrated a positive treatment effect. Therefore switching outcomes, and using a post-hoc analysis, allows for the potential introduction of bias to the review. Indeed, on careful inspection of the minutia of the review, the pre-specified analysis of pooled outcomes demonstrates a non-significant treatment effect, for fatigue at follow-up (exercise therapy versus passive control)

The (non-significant) outcome of this pre-specified pooled analysis of fatigue at follow-up is somewhat buried within the data tables of review, and is very difficult to find; It is not discussed prominently or highlighted. Furthermore, the explanation that the primary outcome was switched, is only briefly mentioned and can easily be missed. Uniquely, for the main outcomes, there is no table outlining the details of the pre-specified pooled analysis of fatigue at follow-up. In contrast, the post-hoc analysis, which has mainly positive outcomes, has been given high prominence throughout the review with little explanation that it is a post-hoc outcome.

So, to reiterate, the (two out of three significant, and one non-significant) post-hoc outcomes for fatigue at follow-up were reported as primary outcomes instead of the (non-significant) pre-specified pooled treatment effect for all eligible studies. Two out of three post-hoc outcomes were significant in effect, however, the pre-specified pooled treatment effect, for the same measures, were not significant (for fatigue at follow-up – exercise therapy versus passive control). Thus, the outcome switching transformed one of the main outcomes of the review, from a non-insignificant effect to a mainly significant effect.

Furthermore, for exercise therapy versus passive control at follow-up, all the other health outcomes were non-significant (except sleep – a secondary outcome), but I believe the casual reader would be unaware of this because it is not explained clearly or prominently in the discussion, and some outcomes have been reported erroneously in the discussion as indicating a significant effect.

All of the above is outlined in my four PDF submissions, with detailed reference to specific sections of the review and specific tables etc.

I believe that the actual treatment effects at follow-up are different to the impression gained from a casual read of the review, or even a careful read of the review. It’s only by an in-depth analysis of the entire review that these issues would be noticed.

In what i believe to be a reasonable request in my submissions, i asked the reviewers to: “Clearly and unambiguously explain that all but one health indicator (i.e. fatigue, physical function, overall health, pain, quality of life, depression, and anxiety, but not sleep) demonstrated a non-significant outcome for pooled treatment effects at follow-up for exercise therapy versus passive control”. My request was not acted upon.

The Cochrane reviewers did provide a reason for the change to the protocol, from a pooled analysis to analyses of groups of mean difference values: “We realise that the standardised mean difference (SMD) is much more difficult to conceptualise and interpret than the normal mean difference (MD) […]”.

However, this is a questionable and unsubstantiated claim, and in my opinion isn’t an adequate explanation or justification for changing the primary outcomes; personally, I find it easier to interpret a single pooled analysis than a group of different analyses with each analysis using a different non-standardised scale to measure fatigue.

Using a SMD is standard practice for Cochrane reviews; Cochrane’s guidance recommends using pooled analyses when the outcomes use different measures, which was the case in this review; Thus i struggle to understand why (in an unplanned change to methodology) using a SMD was considered unhelpful by the reviewers in this case. My PDF document no.4 challenges the reviewers’ reason, with reference to the official Cochrane reviewers’ guidelines.

This review has already led to an academic misunderstanding and mis-reporting of its outcomes, which is demonstrated in the following published letter from one of the co-authors of the IPD protocol……

CMAJ (Canada) recommends exercise for CFS [http://www.cmaj.ca/content/188/7/510/tab-e-letters ]

The letter claims: “We based the recommendations on the Cochrane systematic review which looked at 8 randomised trials of exercise for chronic fatigue, and together showed a consistent modest benefit of exercise across the different patient groups included. The clear and consistent benefit suggests indication rather than contraindication of exercise.”

However, there was not a “consistent modest benefit of exercise” and there was not a “clear and consistent benefit” considering that there were no significant treatment effects for any pre-specified (pooled) health outcomes at follow-up, except for sleep. The actual outcomes of the review seem to contradict the interpretation expressed in the letter.

Even if we include the unplanned analyses in our considerations, then it would still be the case that most outcomes did not indicate a beneficial treatment effect at follow-up for exercise therapy versus passive control. Furthermore, one of the most important outcomes, physical function, did not indicate a significant improvement at follow up (despite the discussion erroneously stating that it was a significant effect).

Two of my submissions discuss other issues, which I will outline below.

My first submission is in relation to the following…

The review states that all the analysed data had previously been formally published and was pre-specified in the relevant published studies. However, the review includes an analysis of external data that had not been formally published and is post-hoc in nature, despite alternative data being available that has been formally published and had been pre-specified in the relevant study. The post-hoc data relates to the FINE trial (Wearden 2010). The use of this data was not in accordance with the Cochrane review’s protocol and also contradicts the review’s stated methodology and the discussion of the review.

Specifically, the fatigue data taken from the FINE trial was not pre-specified for the trial and was not included in the original FINE trial literature. Instead, the data had been informally posted on a BMJ rapid response by the FINE trial investigators[3].

The review analyses post-hoc fatigue data from the FINE trial which is based on the Likert scoring system for the Chalder fatigue questionnaire, whereas the formally published FINE trial literature uses the same Chalder fatigue questionnaires but uses the biomodal scoring system, giving different outcomes for the same patient questionnaires. The FINE trial’s post-hoc Likert fatigue data (used in the review) was initially published by the FINE authors only in a BMJ rapid response post [3], apparently as an after-thought.

This is the response to my first letter…

Larun
Larun said she was “extremely concerned and disappointed” with the Cochrane editors’ actions. “I disagree with the decision and consider it to be disproportionate and poorly justified,” she said.

———————-

Larun said:

Dear Robert Courtney

Thank you for your detailed comments on the Cochrane review ‘Exercise Therapy for Chronic Fatigue Syndrome’. We have the greatest respect for your right to comment on and disagree with our work. We take our work as researchers extremely seriously and publish reports that have been subject to rigorous internal and external peer review. In the spirit of openness, transparency and mutual respect we must politely agree to disagree.

The Chalder Fatigue Scale was used to measure fatigue. The results from the Wearden 2010 trial show a statistically significant difference in favour of pragmatic rehabilitation at 20 weeks, regardless whether the results were scored bi-modally or on a scale from 0-3. The effect estimate for the 70 week comparison with the scale scored bi-modally was -1.00 (CI-2.10 to +0.11; p =.076) and -2.55 (-4.99 to -0.11; p=.040) for 0123 scoring. The FINE data measured on the 33-point scale was published in an online rapid response after a reader requested it. We therefore knew that the data existed, and requested clarifying details from the authors to be able to use the estimates in our meta-analysis. In our unadjusted analysis the results were similar for the scale scored bi-modally and the scale scored from 0 to 3, i.e. a statistically significant difference in favour of rehabilitation at 20 weeks and a trend that does not reach statistical significance in favour of pragmatic rehabilitation at 70 weeks. The decision to use the 0123 scoring did does not affect the conclusion of the review.

Regards,

Lillebeth Larun

——————

In her response, above, Larun discusses the FINE trial and quotes an effect size for post-hoc outcome data (fatigue at follow-up) from the FINE trial that is included in the review. Her quoted figures accurately reflect the data quoted by the FINE authors in their BMJ rapid-response comment [3] but, confusingly, these are slightly different from the data in the Cochrane review. In her response, Larun states that the FINE trial effect size for fatigue at 70 weeks using Likert data is -2.55 (-4.99 to -0.11; p=.040), whereas the Cochrane Review states that it is -2.12 [-4.49, 0.25].

This inconsistency makes this discussion confusing. Unfortunately there is no authoritative source for the data because it had not been formally published when the Cochrane review was published.

It seems that, in her response, Larun has quoted the BMJ rapid response data by Wearden et al.[3], rather than her own review’s data. Referring to her review’s data, Larun says that in “our unadjusted analysis the results were similar for the scale scored bi-modally and the scale scored from 0 to 3, i.e. a statistically significant difference in favour of rehabilitation at 20 weeks and a trend that does not reach statistical significance in favour of pragmatic rehabilitation at 70 weeks”.

It is not clear exactly why there are now two different Likert effect sizes, for fatigue at 70 weeks, but we can be sure that the use of this data undermines the review’s claim that “for this updated review, we have not collected unpublished data for our outcomes…”

This confusion, perhaps, demonstrates one of the pitfalls of using unpublished data. The difference between the data published in the review and the data quoted by Larun in her response (which are both supposedly the same unpublished data from the FINE trial) raises the question of exactly what data has been analysed in the review, and what exactly is the source . If it is unpublished data, and seemingly variable in nature, how are readers expected to scrutinise or trust the Cochrane analysis?

With respect to the FINE trial outcomes (fatigue at 70 week follow-up), Larun has provided the mean differences (effect size) for the (pre-specified) bimodal data and for (post-hoc) Likert data. These two different scoring methods (bimodel and Likert), are used for identical patient Chalder fatigue questionnaires, and provide different effect sizes, so switching the fatigue scoring methods may possibly have had an impact on the review’s primary outcomes for fatigue.

Larun hasn’t provided the effect estimates for fatigue at end-of-treatment, but these would also demonstrate variance between bimodal and Likert scoring, so switching the outcomes might have had a significant impact on the primary outcome of the Cochrane review at end-of-treatment, as well as at follow-up.

Note that the effect estimates outlined in this correspondence, for the FINE trial, are mean differences (this is the data taken from the FINE trial), rather than standardised mean differences (which are sometimes used in the meta-analyses in the Cochrane review); It is important not to get confused between the two different statistical analyses.

Larun said: “The decision to use the 0123 [i.e. Likert] scoring did does [sic] not affect the conclusion of the review.”

But it is not possible for a reader to verify that because Larun has not provided any evidence to demonstrate that switching outcomes has had no effect on the conclusion of the review. i.e. There is no sensitivity analysis, despite the review switching outcomes and using unpublished post-hoc data instead of published pre-specified data. This change in methodology means that the review does not conform to its own protocol and stated methodology. This seems like a significant issue.

Are we supposed to accept the word of the author, rather than review the evidence for ourselves? This is a Cochrane review – renowned for rigour and impartiality.

Note that Larun has acknowledged that I am correct with respect to the FINE trial data used in the review (i.e. that the data was unpublished and not part of the formally published FINE trial study, but was simply posted informally in a BMJ rapid response). Larun confirms that: “…the 33-point scale was published in an online rapid response after a reader requested it. We therefore knew that the data existed, and requested clarifying details from the authors…” But then Larun confusingly (for me) says we must “agree to disagree”.

Larun has not amended her literature to resolve the situation; Larun has not changed her unplanned analysis back to her planned analyses (i.e. to use published pre-specified data as per the review protocol, rather than unpublished post-hoc data); nor has she amended the text of the review so that it clearly and prominently indicates that the primary outcomes were switched. Neither has a sensitivity analysis been published using the FINE trial’s published pre-specified data.

Note the difference in the effect estimates at 70 weeks for bimodal scoring [-1.00 (CI -2.10 to +0.11; p =.076)] vs Likert scoring [-2.55 (-4.99 to -0.11; p=.040)] (as per the Cochrane analysis) or -2.12 [-4.49, 0.25] (also Likert scoring) as per Larun’s response and the BMJ rapid response where the data was initially presented to the public.

Confusingly, there are two different effect sizes for the same (Likert) data; one shows a significant treatment effect and the other shows a non-significant treatment effect. This seems like a rather chaotic situation for a Cochrane review . The data is neither consistent nor transparent. The unplanned Cochrane analysis uses data which has not been published and cannot be scrutinised.

Furthermore, we now have three sets of data for the same outcomes. Because an unplanned analysis was used in the review, it is nearly impossible to work out what is what.

In her response, above, Larun says that both fatigue outcomes (i.e. bimodal & Likert scoring systems) at 70 weeks are non-significant. This is true of the data published in the Cochrane review but, confusingly, this isn’t true if we consider the data that Larun has provided in her response, above. The bimodal and Likert data (fatigue at 70 weeks) presented in the review both have a non-significant effect, however, the Likert data quoted in Larun’s correspondence (which reflects the data in the FINE trial authors’ BMJ rapid response) shows a significant outcome. This may reflect the use of adjusted vs unadjusted data, but it isn’t clear.

Using post-hoc data may allow bias to creep into the review; For example, the Cochrane reviewers might have seen the post hoc data for the FINE trial , because it was posted in an open-access BMJ rapid response [3] prior to the Cochrane review publication date. I am not accusing the authors of conscious bias but Cochrane guidelines are put in place to avoid doubt and to maintain rigour and transparency. Hypothetically, a biased author may have seen that a post-hoc Likert analysis allowed for better outcomes to be reported for the FINE trial. The Cochrane guidelines are established in order to avoid such potential pitfalls and bias, and to avoid the confusion that is inherent in this review.

Note that the review still incorrectly says that all the data is previously published data – even though Larun admits in the letter that it isn’t. (i.e. the data are not formally published in a peer-reviewed journal; i assume that the review wasn’t referring to data that might be informally published in blogs or magazines etc, because the review pretends to analyse formally published data only.)

The authors have practically dismissed my concerns and have not amended anything in the review, despite admitting in the response that they’ve used post-hoc data.

The fact that this is all highly confusing, even after I have studied it in detail, demonstrates that these issues need to be straightened out and fixed.

It surely shouldn’t be the case, in a Cochrane review, that we ( for the same outcomes ) have three sets of results being bandied about, and the data used in a post hoc analysis seems to vary over time, and change from a non-significant treatment effect to a significance treatment effect, depending on where it is quoted. Because it is unpublished, independent scrutiny is made more difficult.

For your information, the BMJ rapid response (Wearden et al.) includes the following data : “Effect estimates [95% confidence intervals] for 20 week comparisons are: PR versus GPTAU -3.84 [-6.17, -1.52], SE 1.18, P=0.001; SL versus GPTAU +0.30 [-1.73, +2.33], SE 1.03, P=0.772. Effect estimates [95% confidence intervals] for 70 week comparisons are: PR versus GPTAU -2.55 [-4.99,-0.11], SE 1.24, P=0.040; SL versus GPTAU +0.36 [-1.90, 2.63], SE 1.15, P=0.752.”

My second submission was in relation to the following…

I believe that properly applying the official Cochrane guidelines would require the review to categorise the PACE trial (White 2011) data as ‘unplanned’ rather than ‘pre-specified’, and would require the risk of bias in relation to ‘selective reporting’ to be categorised accordingly. The Cochrane review currently categorises the risk of ‘selective reporting’ bias for the PACE trial as “low”, whereas the official Cochrane guidelines indicate (unambiguously) that the risk of bias for the PACE data should be “high”. I believe that my argument is fairly robust and water-tight.

This is the response to my second letter…

———————–

Larun said:

Dear Robert Courtney

Thank you for your detailed comments on the Cochrane review ‘Exercise Therapy for Chronic Fatigue Syndrome’. We have the greatest respect for your right to comment on and disagree with our work. We take our work as researchers extremely seriously and publish reports that have been subject to rigorous internal and external peer review. In the spirit of openness, transparency and mutual respect we must politely agree to disagree.

Cochrane reviews aim to report the review process in a transparent way, for example, are reasons for the risk of bias stated. We do not agree that Risk of Bias for the Pace trial (White 2011) should be changed, but have presented it in a way so it is possible to see our reasoning. We find that we have been quite careful in stating the effect estimates and the certainty of the documentation. We note that you read this differently.

Regards,

Lillebeth

————————-

I do not understand what is meant by: “We do not agree that Risk of Bias for the Pace trial (White 2011) should be changed, but have presented it in a way so it is possible to see our reasoning.” …

The review does not discuss the issue of the PACE data being unplanned and I, for one, do not understand the reasoning for not correcting the category for the risk of selective reporting bias. The response to my submission fails to engage with the substantive and serious issues that I raised.

To date, nearly all the issues raised in my letters have been entirely dismissed by Larun. I find this surprising, especially considering that some of the points that I have made were factual (i.e. not particularly open to interpretation) and difficult to dispute. Indeed, Larun’s response even accepts the factual point that I made, in relation to the FINE data, but then confusingly dismisses my request for the issue to be remedied.

There is more detail in the four PDF submissions which are attached to this email, and which have now been published in the latest version of the Cochrane review. I will stop this email now so as not to overwhelm you, and so I don’t repeat myself .

Again, I apologise for the complexity. My four submissions , attached to this email as PDF files, form the basis of my complaint so I ask you to consider them to be the central basis of my complaint . I hope that they will be sufficiently clear.

I trust that you will wish to investigate these issues, with a view to upholding the high standards expected from a Cochrane review.

I look forward to hearing from you in due course. Please feel free to email me at any time with any questions, of if you believe it would be helpful to discuss any of the issues raised.

Regards,

Robert Courtney.

My ‘comments’ (submitted to the Cochrane review authors):

Please note that the four attached PDF documents form the basis of this complaint.

For your convenience, I have included a weblink to a downloadable online copy of each document, and I have attached copies to this email as PDF files, and the comments have now been published in the latest updated version of the review.

The dates refer to the date the comments were submitted to Cochrane.

  1. Query re use of post-hoc unpublished outcome data: Scoring system for the Chalder fatigue scale, Wearden 2010.

Robert Courtney

16th April 2016

https://sites.google.com/site/mecfsnotes/submissions-to-the-cochrane-review-of-exercise-therapy-for-chronic-fatigue-syndrome/fine-trial-unpublished-data

  1. Assessment of Selective Reporting Bias in White 2011.

Robert Courtney

1st May 2016

https://sites.google.com/site/mecfsnotes/submissions-to-the-cochrane-review-of-exercise-therapy-for-chronic-fatigue-syndrome/pace-trial-selective-reporting-bias

  1. A query regarding the way outcomes for physical function and overall health have been described in the abstract, conclusion and discussions of the review.

Robert Courtney

12th May 2016

[ https://sites.google.com/site/mecfsnotes/submissions-to-the-cochrane-review-of-exercise-therapy-for-chronic-fatigue-syndrome/misreporting-of-outcomes-for-physical-function ]

  1. Concerns regarding the use of unplanned primary outcomes in the Cochrane review.

Robert Courtney

3rd June 2016

https://sites.google.com/site/mecfsnotes/submissions-to-the-cochrane-review-of-exercise-therapy-for-chronic-fatigue-syndrome/primary-outcome-switching

References:

  1. Quote from Cochrane reference CD011040:

“Acknowledgements[…]The author team held three meetings in 2011, 2012 and 2013 which were funded as follows: […]2013 via Peter D White’s academic fund (Professor of Psychological Medicine, Centre for Psychiatry, Wolfson Institute of Preventive Medicine, Barts and The London School of Medicine and Dentistry, Queen Mary University of London).”

  1. Larun L, Odgaard-Jensen J, Brurberg KG, Chalder T, Dybwad M, Moss-Morris RE, Sharpe M, Wallman K, Wearden A, White PD, Glasziou PP. Exercise therapy for chronic fatigue syndrome (individual patient data) (Protocol). Cochrane Database of Systematic Reviews 2014, Issue 4. Art. No.: CD011040.

http://onlinelibrary.wiley.com/doi/10.1002/14651858.CD011040/abstract

http://www.cochrane.org/CD011040/DEPRESSN_exercise-therapy-for-chronic-fatigue-syndrome-individual-patient-data

 

  1. Wearden AJ, Dowrick C, Chew-Graham C, et al. Fatigue scale. BMJ Rapid Response. 2010.

http://www.bmj.com/rapid-response/2011/11/02/fatigue-scale-0 (accessed Feb 21, 2016).

End.

Cochrane complaints procedure:

http://www.cochranelibrary.com/help/the-cochrane-library-complaints-procedure.html

The lost last year of one of the key two people in getting the Cochrane review of exercise withdrawn

Did the struggle to get the Cochrane review withdrawn kill Robert Courtney? Or the denial of his basic human rights by the medical system?

mind the brain logo

An incomplete  story that urgently needs to be told. We need to get some conversations going.

Did the struggle to get the Cochrane review withdrawn kill Robert Courtney? Or did the denial of his basic human rights by the medical system?

LONDON, Oct 17 (Reuters) – A respected science journal is to withdraw a much-cited review of evidence on an illness known as chronic fatigue syndrome (CFS) amid fierce criticism and pressure from activists and patients.

robert courtney
Robert Courtney from https://www.meaction.net/2018/03/19/a-tribute-to-robert-courtney/

Citizen scientists and patient advocates Tom Kindlon and Robert Courtney played a decisive role in getting the Cochrane review withdrawn.

In the next few days, I will provide the cover letter email sent by Robert Courtney to Senior Cochrane Editor David Tovey that accompanied his last decisive contribution.  Robert is now deceased.

I will also provide links to Tom Kindlon’s contributions that are just as important.

Readers will be able to see from what David Tuller calls their cogent, persuasive and unassailable submissions that the designation of these two as citizen scientists is well-deserved.

Background

Since 2015, I have kept in touch with an advisory group of about a dozen patients with myalgic encephalomyelitis/chronic fatigue syndrome (ME/cfs). I send emails to myself with this group blind copied. The rationale was that any one of them could respond to me and not have the response revealed to anyone else. A number of patients requested that kind of confidentiality, given the divisions within the patient community.

Robert Courtney was a valued, active member of that group, but then he mysteriously disappeared in January 2017. Patients have their own reasons for entering and withdrawing from social engagement. Sometimes they announce taking leave, sometimes not. I’ve learned to respect absences without challenge, but  I sometimes ask around. In the case of Robert, I could learn nothing from the community except he was not well.

Then in February 2018, Robert reemerged with the email message below. I had assumed his recovery would continue and he would participate in telling his story. Obviously there were a lot more details to tell, but he died by suicide a few weeks later.

Long, unbroken periods of being housebound and often bedridden is one of the curses of having  severe ME/cfs. Able-bodied persons need to understand the reluctance of patients to invite them into their homes.  Even able-bodied persons who believe that they have forged strong bonds with patients on social media.

I nonetheless occasionally make such offers to meet, as I travel through Europe.  I’m typically told things like “sorry, I only leave my house for medical appointments and a twice a year holiday with my family.”

We have to learn not to be offended.

Consequently, few  people who were touched by Robert Courtney and his efforts have ever met him. Most know little about him beyond his strong presence in social media.

From MEpedia, a crowd-sourced encyclopedia of ME and CFS science and history:

Robert Courtney (d. March 7, 2018) was a patient advocate for myalgic encephalomyelitis/chronic fatigue syndrome (ME/CFS) and an outspoken critic of the PACE trial and the biopsychosocial model of chronic fatigue syndrome. He authored numerous published letters in medical journals regarding the PACE trial and, also, filed freedom of information requests in an attempt to get the authors of the PACE trial to release the full trial data to the public for scrutiny.

The day after I received the email below, Robert Courtney sent off to  David Tovey of the Senior Editor Cochrane his final comments.

The email describes the horrible conditions of his last year and his mistreatment and the denial of basic human rights by the medical system. I think airing his story as a wake up call can become another of his contributions to the struggle for the dignity and rights of the patient community.

An excerpt from the email, repeated below.

It seems that this type of mistreatment is all too typical for ME patients. Since I’ve been out of hospital, many patients have told me that they have similar nutritional difficulties, and that they are too scared to seek medical assistance, and that quite a lot of them have been threatened with detention or indeed have been detained under the mental health act. It is a much worse situation than I ever realised.-Robert “Bob” Courtney

We can never know whether Bob’ determined effort to get the review withdrawn led to his medical collapse. The speculation is not just a mindless invoking of “stress kills.” One of the cardinal, defining symptoms of myalgic encephalomyelitis is post exertion malaise.

We usually think of the “exertion” as being physical, but patients with severe form of the illness learn to anticipate that sustained emotional arousal can, within 48 hours or so, put them in their beds for weeks. That applies to positive emotion, like a birthday party, and certainly to negative emotion. Aside from the stress, frustration, and uncertainty of trying to get bad science out of the literature, Bob and other members of the patient community had to contend with enormous vilification and gaslighting, which  still continues today.

After the anorexia diagnosis, they rediagnosed my ME symptoms as being part of a somatoform disorder, and placed me on an eating disorders unit. .-Robert “Bob” Courtney

On Sat, Feb 17, 2018 at 2:44 PM, Bob <brightonbobbob@yahoo.co.uk> wrote:

Hi James,

I don’t know if you’ll remember me. I am an ME patient who was in regular contact with you in 2016. Unfortunately I had a health crisis in early 2017 and I was hospitalised for most of the year. I had developed severe food intolerances and associated difficulties with eating and nutrition. When I admitted myself to hospital they quickly decided there was nothing medically wrong with me and then diagnosed me with anorexia ( to my shock and bewilderment ), and subsequently detained me under the mental health act. I’m not anorexic. The level of ignorance, mistreatment, neglect, abuse, and miscommunication was staggering. After the anorexia diagnosis, they rediagnosed my ME symptoms as being part of a somatoform disorder, and placed me on an eating disorders unit. Then they force-fed me.  It is a very long and troubling story and I’ll spare you the details. I’d quite like a journalist to write up my story but that will have to wait while I address my ongoing health issues.

Unfortunately, it seems that this type of mistreatment is all too typical for ME patients. Since I’ve been out of hospital, many patients have told me that they have similar nutritional difficulties, and that they are too scared to seek medical assistance, and that quite a lot of them have been threatened with detention or indeed have been detained under the mental health act. It is a much worse situation than I ever realised. It is only by sharing my story that people have approached me and been able to tell me what had happened to them. It is such an embarrassing situation both to have eating difficulties and to be detained. The detention is humiliating and the eating difficulties are also excruciatingly embarrassing. Having difficulties with food makes one feel subhuman. So I have discovered that many patients keep their stories to themselves.

You might remember that in 2016 I submitted four lengthy comments to Cochrane with respect to the exercise therapy for chronic fatigue syndrome review. . Before hospital, I had also written an incomplete draft complaint to follow up my submitted comments, but my health crisis interrupted the process and so I haven’t yet sent it .

I am out of hospital now and have finished editing the complaint and I am about to send it. I am going to blind copy you into the complaint so this email is just to let you know to expect it. I’ll probably send it within the next 24 hours. The complaint isn’t as concise or carefully formatted as it could be because I’m still unwell and I have limited capacity.

Anyway this is just to give you some advance notice. I hope this email finds you in good spirits. I haven’t been keeping up to date with the news and activities, while I’ve been away, but I see there’s been a lot of activity. Thanks so much your ongoing efforts.

Best wishes,

Bob (Robert Courtney)

My replies

James Coyne <jcoynester@gmail.com>

Feb 17, 2018, 2:50 PM

to Bob

Bob, I remember you well as one of the heroes of the patient movement, and a particularly exemplary hero because you so captured my idea or of the citizen scientist gathering the data and the sense of methodology to understand the illness and battle the PACE people. I’m so excited to see your reemergence. I look forward to what you send.

Warmest regards

Jim

James Coyne <jcoynester@gmail.com>

Feb 17, 2018, 3:11 PM

to Bob

Your first goal must be to look after yourself and keep yourself as active and well as possible. You know, the patient conception of pacing. You are an important model and resource for lots of people

But when you are ready, I look forward to your telling your story and how it fits with others.

Warmest of regards

Jim

Effect of a missing clinical trial on what we think about cognitive behavior therapy

  • Data collection for a large, well-resourced study of cognitive behavior therapy (CBT) for psychosis was completed years ago, but the study remains unpublished.
  • Its results could influence the overall evaluation of CBT versus alternative treatments if integrated with what is already known.
  • Political considerations can determine whether completed psychotherapy studies get published or remain lost.
  • This rich example demonstrates the strong influence of publication bias on how we assess psychotherapies.
  • What can be done to reduce the impact of this particular study having gone missing?

A few years ago Ben Goldacre suggested that we do a study of the registration of clinical trials.

lets'collaborate

I can’t remember the circumstances, but Goldacre and I did not pursue the idea further. I was already committed to studying psychological interventions, in which Goldacre was much less interested. Having battled to get American Psychological Association to fully accept and implement CONSORT in its journals, I was well aware how difficult it was getting the professional organizations offering the prime outlets for psychotherapy studies to accept needed reform. I wanted to stay focused on that.

I continue to follow Goldacre’s work closely and cite him often. I also pay particular attention to John Ioannidis’ follow up of his documentation that much of what we found in the biomedical literature is false or exaggerated, like:

Ioannidis JP. Clinical trials: what a waste. BMJ. 2014 Dec 10;349:g7089

Many trials are entirely lost, as they are not even registered. Substantial diversity probably exists across specialties, countries, and settings. Overall, in a survey conducted in 2012, only 30% of journal editors requested or encouraged trial registration.

In a seeming parallel world, I keep showing that in psychology the situation is worse. I had a simple explanation why that I now recognize was naïve: Needed reforms enforced by regulatory bodies like the US Food and Drug Administration (FDA) take longer to influence the psychotherapy literature, where there are no such pressures.

I think we now know that in both biomedicine and, again, psychology, that broad declarations of government and funding bodies and even journals’ of a commitment to disclose a conflict of interest, registering trials, sharing data, are insufficient to ensure that the literature gets cleaned up.

Statements were published across 14 major medical journals endorsing routine data sharing]. Editors of some of the top journals immediately took steps to undermine the implementation in their particular journals. Think of the specter of “research parasites, raised by the editors of New England Journal of Medicine (NEJM).

Another effort at reform

Following each demonstration that reforms are not being implemented, we get more pressures to do better. For instance, the 2015 World Health Organization (WHO) position paper:

Rationale for WHO’s New Position Calling for Prompt Reporting and Public Disclosure of Interventional Clinical Trial Results

WHO’s 2005 statement called for all interventional clinical trials to be registered. Subsequently, there has been an increase in clinical trial registration prior to the start of trials. This has enabled tracking of the completion and timeliness of clinical trial reporting. There is now a strong body of evidence showing failure to comply with results-reporting requirements across intervention classes, even in the case of large, randomised trials [37]. This applies to both industry and investigator-driven trials. In a study that analysed reporting from large clinical trials (over 500 participants) registered on clinicaltrials.gov and completed by 2009, 23% had no results reported even after a median of 60 months following trial completion; unpublished trials included nearly 300,000 participants [3]. Among randomised clinical trials (RCTs) of vaccines against five diseases registered in a variety of databases between 2006–2012, only 29% had been published in a peer-reviewed journal by 24 months following study completion [4]. At 48 months after completion, 18% of trials were not reported at all, which included over 24,000 participants. In another study, among 400 randomly selected clinical trials, nearly 30% did not publish the primary outcomes in a journal or post results to a clinical trial registry within four years of completion [5].

Why is this a problem?

  • It affects understanding of the scientific state of the art.

  • It leads to inefficiencies in resource allocation for both research and development and financing of health interventions.

  • It creates indirect costs for public and private entities, including patients themselves, who pay for suboptimal or harmful treatments.

  • It potentially distorts regulatory and public health decision making.

Furthermore, it is unethical to conduct human research without publication and dissemination of the results of that research. In particular, withholding results may subject future volunteers to unnecessary risk.

How the psychotherapy literature is different from a medical literature.

Unfortunately for the trustworthiness of the psychotherapy literature, the WHO statement is limited to medical interventions. We probably won’t see any direct effects on the psychotherapy literature anytime soon.

The psychotherapy literature has all the problems in implementing reforms that we see in biomedicine – and more. Professional organizations like the American Psychological Association and British Psychological Society publishing psychotherapy research have the other important function of ensuring their clinical membership developer’s employment opportunities. More opportunities for employment show the organizations are meeting their members’ needs this results in more dues-paying members.

The organizations don’t want to facilitate third-party payers citing research that particular interventions that their membership is already practicing are inferior and need to be abandoned. They want the branding of members practicing “evidence-based treatment” but not the burden of members having to make decisions based on what is evidence-based. More basically, psychologists’ professional organizations are cognizant of the need to demonstrate a place in providing services that are reimbursed because they improve mental and physical health. In this respect, they are competing with biomedical interventions for the same pot of money.

So, journals published by psychological organizations have vested interests and not stringently enforcing standards. The well-known questionable research practices of investigators are strengthened by questionable publication practices, like confirmation bias, that are tied to the organizations’ institutional agenda.

And the lower status journals that are not published by professional organizations may compromise their standards for publishing psychotherapy trials because of the status that having these articles confers.

Increasingly, medical journals like The Lancet and The Lancet Psychiatry are seen as more prestigious for publishing psychotherapy trials, but they take less seriously the need to enforce standards for psychotherapy studies the regulatory agencies require for biomedical interventions. Example: The Lancet violated its own policies and accepted publication Tony Morrison’s CBT for psychosis study  for publication when it wasn’t registered until after the trial and started. The declared outcomes were vague enough so they could be re-specified after results were known .

Bottom line, in the case of publishing all psychotherapy trials consistent with published protocols: the problem is taken less seriously than if it were a medical trial.

Overall, there is less requirement for psychotherapy trials be registered and less attention paid by editors and reviewers as to whether trials were registered, and whether outcomes are analytic plans were consistent between the registration in the published study.

In a recent blog post, I identified results of a trial that had been published with switched outcomes and then re-published in another paper with different outcomes, without the registration even being noted.

But for all the same reasons cited by the recent WHO statement, publication of all psychotherapy trials matters.

archaeologist digging for goldRecovering an important CBT trial gone missing

I am now going to review the impact of a large, well resourced study of CBT for psychosis remaining on published. I identified the study by a search of the ISRCTN:

The ISRCTN registry is a primary clinical trial registry recognised by WHO and ICMJE that accepts all clinical research studies (whether proposed, ongoing or completed), providing content validation and curation and the unique identification number necessary for publication. All study records in the database are freely accessible and searchable.

I then went back to the literature to see what it happened with it. Keep in mind that this step is not even possible for the many psychotherapy trials that are simply not registered at all.

Many trials are not registered because they are considered pilot and feasibility studies and therefore not suitable for entering effect sizes into the literature. Yet, if significant results are found, they will be exaggerated because they come from an underpowered study. And such results become the basis for entering results into the literature as if it were a planned clinical trial, with considerable likelihood of not being able to be replicated.

There are whole classes of clinical and health psychology interventions that are dominated by underpowered, poor quality studies that should have been flagged as for evidence or excluded altogether. So, in centering on this trial, I’m picking an important example because it was available to be discovered, but there is much of their there is not available to be discovered, because it was not registered.

CBT versus supportive therapy for persistent positive symptoms in psychotic disorders

The trial registration is:

Cognitive behavioural treatment for persistent positive symptoms in psychotic disorders SRCTN29242879DOI 10.1186/ISRCTN29242879

The trial registration indicates that recruitment started on January 1, 2007 and ended on December 31, 2008.

No publications are listed. I and others have sent repeated emails to the principal investigator inquiring about any publications and have failed to get a response. I even sent a German colleague to visit him and all he would say was that results were being written up. That was two years ago.

Google Scholar indicates the principal investigator continues to publish, but not the results of this trial.

A study to die for

The study protocol is available as a PDF

Klingberg S, Wittorf A, Meisner C, Wölwer W, Wiedemann G, Herrlich J, Bechdolf A, Müller BW, Sartory G, Wagner M, Kircher T. Cognitive behavioural therapy versus supportive therapy for persistent positive symptoms in psychotic disorders: The POSITIVE Study, a multicenter, prospective, single-blind, randomised controlled clinical trial. Trials. 2010 Dec 29;11(1):123.

The methods section makes it sound like a dream study with resources beyond what is usually encountered for psychotherapy research. If the protocol is followed, the study would be an innovative, large, methodologically superior study.

Methods/Design: The POSITIVE study is a multicenter, prospective, single-blind, parallel group, randomised clinical trial, comparing CBT and ST with respect to the efficacy in reducing positive symptoms in psychotic disorders. CBT as well as ST consist of 20 sessions altogether, 165 participants receiving CBT and 165 participants receiving ST. Major methodological aspects of the study are systematic recruitment, explicit inclusion criteria, reliability checks of assessments with control for rater shift, analysis by intention to treat, data management using remote data entry, measures of quality assurance (e.g. on-site monitoring with source data verification, regular query process), advanced statistical analysis, manualized treatment, checks of adherence and competence of therapists.

The study was one of the rare ones providing for systematic assessments of adverse events and any harm to patients. Preumably if CBT is powerful enough to affect positive change, it can have negative effects as well. But these remain entirely a matter of speculation.

Ratings of outcome were blinded and steps were taken to preserve the blinding even if an adverse event occurred. This is important because blinded trials are less susceptible to investigator bias.

Another unusual feature is the use of a supportive therapy (ST) credible, but nonspecific condition as a control/comparison.

ST is thought as an active treatment with respect to the patient-therapist relationship and with respect to therapeutic commitment [21]. In the treatment of patients suffering from psychotic disorders these ingredients are viewed to be essential as it has been shown consistently that the social network of these patients is limited. To have at least one trustworthy person to talk to may be the most important ingredient in any kind of treatment. However, with respect to specific processes related to modification of psychotic beliefs, ST is not an active treatment. Strategies specifically designed to change misperceptions or reasoning biases are not part of ST.

Use of this control condition allows evaluation of the important question of whether any apparent effects of CBT are due to the active ingredients of that approach or to the supportive therapeutic relationship within which the active ingredients are delivered.

Being able to rule out the effects of CBT are due to nonspecific effects justifies the extra resources needed to provide specialized training in CBT, if equivalent effects are obtained in the ST group, it suggests that equivalent outcomes can be achieved simply by providing more support to patients, presumably by less trained and maybe even lay personnel.

It is a notorious feature of studies of CBT for psychosis that they lack comparison/control groups in any way equivalent to the CBT in terms of nonspecific intensity, support, encouragement, and positive expectations. Too often, the control group are ill-defined treatment as usual (TAU) that lacks regular contact and inspires any positive expectations. Basically CBT is being compared to inadequate treatment and sometimes no treatment and so any apparent effects that are observed are due to correcting these inadequacies, not any active ingredient.

The protocol hints in passing at the investigators’ agenda.

This clinical trial is part of efforts to intensify psychotherapy research in the field of psychosis in Germany, to contribute to the international discussion on psychotherapy in psychotic disorders, and to help implement psychotherapy in routine care.

Here we see an aim to justify implementation of CBT for psychosis in routine care in Germany. We have seen something similar with repeated efforts of German to demonstrate that long-term psychodynamic psychotherapy is more effective than shorter, less expensive treatments, despite the lack of credible data [ ].

And so, if the results would not contribute to getting psychotherapy implemented in routine care in Germany, do they get buried?

Science & Politics of CBT for Psychosis

A rollout of a CBT study for psychosis published in Lancet made strong claims in a BBC article and audiotape promotion.

morroson slide-page-0

 

 

 

The attention attracted critical scrutiny that these claims couldn’t sustain. After controversy on Twitter, the BBC headline was changed to a more modest claim.

Criticism mounted:

  • The study retained fewer participants receiving CBT at the end of the study than authors.
  • The comparison treatment was ill-defined, but for some patients meant no treatment because they were kicked out of routine care for refusing medication.
  • A substantial proportion of patients assigned to CBT began taking antipsychotic medication by the end of the study.
  • There was no evidence that the response to CBT was comparable to that achieved with antipsychotic medication alone in clinical trials.
  • No evidence that less intensive, nonspecific supportive therapy would not have achieved the same results as CBT.

And the authors ended up conceding in a letter to the editor that their trial had been registered after data collection had started and it did not produce evidence of equivalence to antipsychotic medication.

In a blog post containing the actual video of the presentation before his British Psychological Society, Keith Laws declares

Politics have overcome the science in CBT for psychosis

Recently the British Psychological Society invited me to give a public talk entitled CBT: The Science & Politics behind CBT for Psychosis. In this talk, which was filmed…, I highlight the unquestionable bias shown by the National Institute of Clinical Excellence (NICE) committee  (CG178) in their advocacy of CBT for psychosis.

The bias is not concealed, but unashamedly served-up by NICE as a dish that is high in ‘evidence-substitute’, uses data that are past their sell-by-date and is topped-off with some nicely picked cherries. I raise the question of whether committees – with such obvious vested interests – should be advocating on mental health interventions.

I present findings from our own recent meta-analysis (Jauhar et al 2014) showing that three-quarters of all RCTs have failed to find any reduction in the symptoms of psychosis following CBT. I also outline how trials which have used non-blind assessment of outcomes have inflated effect sizes by up to 600%. Finally, I give examples where CBT may have adverse consequences – both for the negative symptoms of psychosis and for relapse rates.

A pair of well-conducted and transparently reported Cochrane reviews suggest there is little evidence for the efficacy of CBT for psychosis (*)

cochrane slide-page-0                          cochrane2-page-0

 

These and other slides are available in a slideshow presentation of a talk I gave at the Edinburgh Royal  Infirmary.

Yet, even after having to be tempered in the face of criticism, the original claims of the Morrison study get echoed in the antipsychiatry Understanding Psychosis:

“Other forms of therapy can also be helpful, but so far it is CBTp that has been most intensively researched. There have now been several meta-analyses (studies using a statistical technique that allows findings from various trials to be averaged out) looking at its effectiveness. Although they each yield slightly different estimates, there is general consensus that on average, people gain around as much benefit from CBT as they do from taking psychiatric medication.”

Such misinformation can confuse patients making difficult decisions about whether to accept antipsychotic medication.

go on without mejpgIf the results from the missing CBT for psychosis study became available…

If the Klingberg study were available and integrated with existing data, it would be one of the largest and highest quality studies and it would provide insight into any advantage of CBT for psychosis. For those who can be convinced by data, a null finding from a large studythat added to mostly small and methodologically unsophisticated studies could be decisive.

A recent meta-analysis of CBT for prevention of psychosis by Hutton and Taylor includes six studies and mentions the trial protocol in passing:

Two recent trials of CBT for established psychosis provide examples of good practice for reporting harms (Klingberg et al. 20102012) and CONSORT (Consolidated Standards of Reporting Trials) provide a sensible set of recommendations (Ioannidis et al. 2004).

Yet, it does not provide indicate why it is missing and is not included in a list of completed but unpublished studies. Yet, the protocol indicates a study considerably larger than any of the studies that were included.

To communicate a better sense of the potential importance of this missing study and perhaps place more pressures on the investigators to release its results, I would suggest that future meta-analyses state:

The protocol for Klingberg et al. Cognitive behavioural treatment for persistent positive symptoms in psychotic disorders indicates that recruitment was completed in 2008. No publications have resulted. Emails to Professor Klingberg about the status of the study failed to get a response. If the study were completed consistent with its protocol, it would represent one of the largest studies of CBT for psychosis ever and one of the few with a fair comparison between CBT and supportive therapy. Inclusion of the results could potentially substantially modify the conclusions of the current meta-analysis.